Safety and Efficacy Study of a Fluoroquinolone to Treat Complicated Skin Infections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of a Fluoroquinolone to Treat Complicated Skin Infections (NCT00719810), a randomized phase 2 study. The primary outcome is Clinical Response at Test of Cure (TOC) in the Clinically Evaluable (CE) Population.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, multicenter, parallel-group phase 2 study. The registry lists quadruple masking; it does not identify which groups of people were masked. The study status is completed, and its enrollment is listed as 150. The registry records a start in 2008-06 and primary completion in 2008-10.

Participants were assigned to one of three intravenous regimens: delafloxacin 300 mg every 12 hours, delafloxacin 450 mg every 12 hours, or tigecycline 100 mg as an initial dose followed by 50 mg every 12 hours. The posted primary outcome counts are 33 of 35 for the lower-dose delafloxacin arm, 37 of 40 for the higher-dose arm, and 31 of 34 for tigecycline. These outcome denominators represent the clinically evaluable population, not the overall enrollment.

The primary outcome was clinical response at test of cure, assessed 14-21 days after the last study-drug dose. The registry defines the clinically evaluable population using treatment exposure, attendance at the test-of-cure visit, and the absence of concomitant systemic antibacterial therapy active against the causative pathogen. A secondary outcome assessed clinical response among patients with MRSA.

The registry record does not report the randomization procedure, allocation concealment details, the number of centers, the original sample-size justification, or the planned statistical analysis strategy. It also does not give arm-specific descriptions beyond the listed regimens. The recorded design features therefore establish the broad comparison but do not resolve all details of how the trial was conducted or planned.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The CE population included patients with a diagnosis of cSSSI who received at least 80% of study drug, had a test of cure (TOC) visit 14-21 days after the last dose of study drug, and who did not receive any concomitant, systemic antibacterial therapy with activity against the causative pathogen.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Clinical Response at Test of Cure (TOC) in the Clinically Evaluable (CE) Population, measured over 14-21 days after the last dose of study drug.

The primary endpoint counts participants classified as having a clinical response at test of cure in the clinically evaluable population. The visit took place 14-21 days after the last dose of study drug. The registry defines cure as resolution of baseline signs and symptoms, or improvement to a degree that no further antibiotic treatment is needed. Failure included needing additional antibiotics because of inadequate efficacy after at least 2 days of study treatment, treatment-related adverse events, and/or surgical intervention more than 48 hours after study entry.

A clinical response endpoint is intended to summarize the participant’s clinical status at a specified follow-up visit using a prespecified outcome definition. In general, a binary outcome such as response or failure is easy to interpret as a count of participants meeting the definition. It also depends on the exact criteria and assessment time: a response at test of cure is not the same measure as a response at another visit or a microbiological outcome.

The clinically evaluable restriction matters to interpretation. It excludes people who did not meet the listed treatment, visit, or concomitant-therapy conditions, so the primary counts describe that defined subset rather than every enrolled participant. The registry record does not report how participants excluded from this population were handled in an alternative primary analysis.

7. Results Posted in the Registry

• Delafloxacin 450 mg IV q12h: 92.5% (37/40) versus 94.3% (33/35) on control; risk difference -1.8 percentage points (95% CI -13.0 to 9.4), risk ratio 0.98 (0.87–1.11); unadjusted two-proportion z-test p = 0.757.
• Tigecycline 100 mg IV x 1, Followed by 50 mg IV q12h: 91.2% (31/34) versus 94.3% (33/35) on control; risk difference -3.1 percentage points (95% CI -15.4 to 9.1), risk ratio 0.97 (0.85–1.10); unadjusted two-proportion z-test p = 0.618.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Clinical Response in Patients With Methicillin-resistant Staphylococcus Aureus (MRSA)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Delafloxacin 450 mg IV q12h: 95.0% (19/20) versus 92.9% (13/14) on control; risk difference 2.1 percentage points (95% CI -14.4 to 18.7), risk ratio 1.02 (0.86–1.22); unadjusted two-proportion z-test p = 0.794.
  • Tigecycline 100 mg IV x 1, Followed by 50 mg IV q12h: 85.7% (12/14) versus 92.9% (13/14) on control; risk difference -7.1 percentage points (95% CI -29.9 to 15.6), risk ratio 0.92 (0.71–1.20); unadjusted two-proportion z-test p = 0.541.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delafloxacin 450 mg IV q12h and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tigecycline 100 mg IV x 1, Followed by 50 mg IV q12h and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: clinical response among participants with MRSA, assessed at the same 14-21 days after the last dose of study drug. The posted counts are 13 of 14 for delafloxacin 300 mg, 19 of 20 for delafloxacin 450 mg, and 12 of 14 for tigecycline. As with the primary outcome, most assessed participants in each arm met the response definition. The comparative intervals are broad and include differences in either direction, so the subgroup results do not establish a clear ordering among the regimens.

The secondary pattern is broadly consistent with the primary result in that response counts are high in every arm and the comparisons remain uncertain. It does not independently confirm the primary comparison. The MRSA subgroup has fewer participants than the primary clinically evaluable group, so its estimates have less information and are especially sensitive to individual outcomes. A subgroup estimate can also differ from an overall estimate through random variation; the registry record does not report a formal interaction analysis testing whether treatment contrasts differ by MRSA status.

Unadjusted secondary results generally carry less inferential weight than a prespecified primary analysis because many outcomes or subgroup comparisons can increase the chance of apparently notable results arising by chance. This is a general multiplicity concern, not evidence that any particular result is spurious. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a statistical analysis plan specifying how the secondary outcome would be interpreted. The secondary findings are therefore best treated as descriptive and exploratory rather than as a stand-alone basis for a firm comparative conclusion.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Clinical Response in Patients With Methicillin-resistant Staphylococcus Aureus (MRSA)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary: each clinically evaluable participant is counted as having either a clinical response or not having one. The registry gives counts in each arm, not an average score or a rate measured repeatedly over time. The outcome definition combines clinical improvement with the need for further intervention or treatment, as described in the endpoint definition. General statistical interpretation of a binary endpoint begins with the number meeting the definition and the number assessed in each group; comparative estimates then describe how the groups differ.

What does a risk difference describe?

A risk difference compares the event proportions in two groups by subtracting one group’s proportion from the other’s. In these posted comparisons, the reference group is delafloxacin 300 mg, and each estimate is for the named other arm relative to that reference. A negative estimate means the observed response proportion in the named arm was lower than in the reference arm; a positive estimate would mean it was higher. The risk difference keeps the comparison on the absolute-proportion scale, which can be read as a difference in the share of participants meeting the response definition.

The registry also includes risk ratios and odds ratios for the primary and secondary comparisons. General interpretation differs by scale: a risk ratio compares proportions as a ratio, while an odds ratio compares the odds of the outcome. Each measure answers a related but distinct question. For these small group counts, the interval estimates for those measures are broad, and their values should be considered alongside the direct event counts and risk-difference estimates. The registry record does not identify which effect measure was designated as the primary inferential measure in a prespecified plan.

What do the p-values add?

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. The posted p-values are unadjusted. They should therefore be interpreted as individual comparisons rather than as accounting for all outcomes or all possible comparisons in the study. The registry record does not report a multiplicity strategy or a prespecified testing hierarchy.

For the primary comparisons, the posted unadjusted p-values are 0.757 for delafloxacin 450 mg versus 300 mg and 0.618 for tigecycline versus 300 mg. These values do not provide strong evidence against equal response proportions under the conventional null comparison, but they cannot establish equivalence or prove that the groups have identical response. Equivalence or noninferiority requires a defined margin and a design and analysis tailored to that question; such information is not reported in the registry record.

Why does the analysis population matter?

The primary endpoint is reported for the clinically evaluable population, which the registry defines by diagnosis, receiving at least 80% of study drug, attending the test-of-cure visit, and not receiving specified concomitant systemic antibacterial therapy. This is a post-randomization subset. General statistical reasoning recognizes that restricting analysis after randomization can affect how well the original randomized comparison is preserved, depending on why participants are excluded. The registry record does not report the numbers excluded for each reason or an analysis of all randomized participants. It is therefore not possible to assess from the posted primary counts how sensitive the comparison is to those exclusions.

The secondary MRSA outcome is also binary and has fewer participants in each arm than the primary evaluable analysis. Its estimates are correspondingly uncertain. The registry lists no reported secondary analyses, so the posted counts and comparisons should not be mistaken for a fully documented inferential analysis. In general, outcomes and analysis populations need clear definitions, prespecification, and transparent handling of missing observations to support reliable interpretation. Those protocol and analysis details are not reported in the registry record.

What can recalculation establish?

Recalculated comparisons based on posted summary counts are simple, unadjusted comparisons. They can help express the observed group contrast on common statistical scales, but they do not reproduce any unavailable adjusted or prespecified sponsor analysis. The registry does not flag a discrepancy between the posted results and the recalculated estimates. No adjustment for covariates, stratification factors, or center effects is reported in the registry record, so none should be assumed.

General statistical methods also distinguish estimation from decision-making. A point estimate summarizes the observed contrast, an interval conveys uncertainty under the calculation’s assumptions, and a p-value summarizes compatibility with a null hypothesis. None supplies information absent from the trial design, such as the intended margin for noninferiority, the planned primary comparison, or the handling of missing outcomes. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a group difference. The posted primary risk-difference intervals are wide enough to include both a negative and a positive value. For delafloxacin 450 mg versus delafloxacin 300 mg, the interval runs from -0.13 to 0.094. For tigecycline versus delafloxacin 300 mg, it runs from -0.154 to 0.091. Thus, the posted data do not pinpoint the direction or size of the comparative difference with high precision.

In general, a confidence interval is a range generated by a statistical procedure that reflects uncertainty in an estimate under its assumptions. The registry record does not state the confidence level for the posted intervals, so no level should be inferred. An interval spanning zero for a difference is compatible with no difference, but also with differences in either direction. It is not evidence that the true effect is exactly zero.

The arm-specific primary denominators are 35, 40, and 34, and the MRSA secondary denominators are smaller still. Limited numbers of observations commonly produce less precise estimates. The interval widths make that uncertainty visible; the high response counts do not remove it. Different effect scales also have different interval ranges and interpretations, so an interval for a risk ratio or odds ratio should not be read as if it were a risk-difference interval.

Precision is distinct from bias. A narrow interval would not rule out bias from outcome selection or missing data, and a broad interval does not imply that the estimate is systematically wrong. Because the registry record does not report missing-data handling, the number and reasons for exclusions, or a full analysis population comparison, the intervals alone cannot address those concerns.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations give participants per arm for the binary outcomes; they do not give total events. The calculations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. Rows planning for 100%, 75%, and 50% of the observed effect therefore ask what group size would be needed under those different assumed target effects.

The 80% power column describes a planning scenario in which a study has an 80% chance of detecting the specified effect at the stated significance level, if the assumptions used for the calculation hold. The 90% column uses a higher target chance of detecting that same assumed effect and consequently calls for more participants per arm. These are planning illustrations computed from observed effects, not the trial’s original design calculations; the original sample-size assumptions are not reported in the registry record.

Smaller assumed effects require more participants because they are harder to distinguish from ordinary sampling variation. This relationship is why the rows using a smaller fraction of the observed effect call for larger group sizes. The estimates depend on the observed effect used as a starting point, which itself is uncertain in a study with limited arm-specific counts. They should not be treated as a definitive recommendation for a future study without a separate design rationale.

This is not observed power. Observed power is not a useful substitute for interpreting the estimated effect and its uncertainty after a study is complete. The planning figures instead illustrate how sample size changes under specified assumptions about the target effect, allocation, significance level, and calculation method. The registry record does not report whether these assumptions were used when the original trial was designed.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.943; treatment proportion p₁ = 0.925; average p̄ = 0.934.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3513 = 0.6885.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3511 = 0.2955.
4. n = (0.6885 + 0.2955)² / (-0.0179)² = 3,036.5, rounded up to 3,037 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.942857142857143                          # control proportion
p1 <- 0.925                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(719810)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 3,037 (80% power), 4,065 (90% power)
 75% of observed effect: n per arm = 5,230 (80% power), 7,000 (90% power)
 50% of observed effect: n per arm = 11,383 (80% power), 15,238 (90% power)
power.prop.test: 3036.5 
Simulated power at n = 3,037 per arm: 0.804 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines more than one outcome, treatment contrast, subgroup, or analysis. In general, as the number of statistical tests grows, the chance of at least one apparently notable result can increase if every test is interpreted independently. Statistical plans may address this through a testing hierarchy or an adjustment to the inference. The registry record does not report whether any such approach was planned or used.

The record lists a primary clinical-response endpoint and one secondary clinical-response endpoint for patients with MRSA. It includes two between-arm comparisons against delafloxacin 300 mg for the primary endpoint and two for the secondary endpoint. The posted p-values are unadjusted. The registry record does not identify which comparisons, if any, were intended as confirmatory, nor does it report a prespecified alpha allocation or a family-wise error strategy. Consequently, the p-values should not be read as though they account for all outcomes and comparisons.

The record reports no analyses in the secondary-outcome entry and no reported analyses in the analysis listing. The statistical analysis plan, covariate adjustment, stratification, and any interim analyses are not reported in the registry record. Their absence from the record does not establish that such procedures were or were not used; it means their role cannot be evaluated from the posted information.

The primary analysis population is defined as clinically evaluable. It includes patients with cSSSI who received at least 80% of study drug, attended the test-of-cure visit, and did not receive concomitant systemic antibacterial therapy active against the causative pathogen. The registry record does not report an intention-to-treat analysis, a modified intention-to-treat definition, or a comparison of results across analysis populations. It also does not report counts and reasons for exclusion from the clinically evaluable population or the method used to handle missing outcome observations.

These details matter because missingness and exclusions can affect both the precision and interpretation of treatment comparisons. General statistical practice calls for clear reporting of analysis populations and missing-data methods. Without those details, readers cannot determine whether the posted results are robust to alternative approaches to participant inclusion or missing outcomes.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: femoral neck fracture (2.0%), cellulitis (2.0%), cerebellar infarction (2.0%), duodenal ulcer hemorrhage (2.0%), subclavian vein thrombosis (2.0%).

The safety record gives numbers of participants at risk and numbers affected by serious adverse events and other adverse events. For serious adverse events, the counts are 1 of 49 in the delafloxacin 300 mg group, 3 of 51 in the delafloxacin 450 mg group, and 3 of 50 in the tigecycline group. For other adverse events, the counts are 14 of 49, 32 of 51, and 36 of 50, respectively. These are descriptive counts; they are not adjusted comparisons.

The listed serious adverse-event terms include femoral neck fracture, cellulitis, cerebellar infarction, duodenal ulcer hemorrhage, subclavian vein thrombosis, and bradycardia, each recorded as 2.0%. The registry record does not provide enough information in this summary to attribute these terms to a particular arm or to establish causality. Death counts are not reported in the registry record.

Safety counts should be interpreted alongside the group denominators, event definitions, follow-up, and methods of collection. The registry record does not provide detailed timing, severity grading, exposure-adjusted rates, or a statistical comparison for these data. The counts alone do not establish whether an event was caused by a study drug.

16. What the Result Does, and Does Not, Mean

The posted results show that clinical response was recorded for many participants in each clinically evaluable arm. The between-arm risk-difference estimates are close to zero, but their reported intervals span values on either side of zero. The study therefore offers estimates with substantial uncertainty, rather than a precise determination of the direction or size of a difference.

A lack of a clearly distinguished result is not proof that the regimens have identical effects. Equivalence requires a prespecified margin and an analysis designed to test whether differences fall within that margin; the margin and such a design are not reported in the registry record. Likewise, a non-significant p-value does not demonstrate noninferiority. These results should not be described as proving that one regimen works, fails, or is interchangeable with another.

The primary counts apply to the clinically evaluable population, not necessarily to all randomized participants. The criteria for this population involve treatment exposure, attendance at a follow-up visit, and concomitant antibacterial therapy. The registry record does not report the full disposition of randomized participants or an all-randomized analysis, limiting interpretation beyond those meeting the criteria.

The MRSA secondary results are based on fewer participants and also leave considerable uncertainty about comparative effects. The record does not report a multiplicity plan or a statistical analysis plan, so unadjusted secondary comparisons should be regarded cautiously. Safety counts are descriptive and do not establish causation or provide a complete comparative safety assessment.

In general, a trial result is interpreted by combining its design, population, outcome definition, estimates, uncertainty, and reporting completeness. Here, the registry gives a defined clinical endpoint and observed arm counts, but several details needed to assess robustness are not reported. The evidence describes the outcomes recorded in this study; it does not settle broader clinical questions or provide medical advice.

17. Why This Trial Matters Statistically

This trial illustrates why event counts and comparative uncertainty need to be read together. Response counts are high in all three clinically evaluable groups, but the direct comparisons have broad intervals crossing no difference. A pattern of many responses within each arm is not the same as precise evidence that the arms differ or are equivalent.

It also highlights the consequences of defining an analysis population after randomization. The primary result is restricted to participants who met the clinically evaluable criteria, while the registry record does not report an all-randomized analysis or the disposition of participants outside that group. Such information helps readers assess how well randomization is retained in the analysis and how far the result can be generalized.

The MRSA outcome demonstrates a further statistical issue: subgroup findings can be less precise when based on fewer participants, and secondary comparisons require attention to multiplicity and prespecification. The registry record reports unadjusted comparisons but not a plan describing how multiple outcomes or comparisons were to be handled.

Finally, the sample-size illustrations show how planning depends on assumed effect size, allocation, and target power, while the original study’s sample-size rationale is not reported. Together, these features make the study useful for teaching careful interpretation of phase 2 results: distinguish descriptive counts from comparative estimates, read intervals as uncertainty, and avoid conclusions that require unreported design or analysis details.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary comparison uses the clinically evaluable population, defined by treatment exposure, a completed test-of-cure visit, and restrictions on concomitant antibacterial therapy. The registry record does not report how many randomized participants failed each criterion, why they were excluded, or whether an analysis of all randomized participants gave a similar result. This limits assessment of selection related to the primary analysis.

The evaluable arm sizes are 35, 40, and 34, and the MRSA subgroup sizes are 14, 20, and 14. The posted comparative intervals are broad, particularly for the secondary subgroup comparisons. The registry record does not report a sample-size justification for the original design, so it is not possible to determine what treatment difference the trial was designed to detect.

The record identifies unadjusted comparisons but does not report the statistical analysis plan, multiplicity handling, missing-data procedures, covariate adjustments, or interim analyses. The confidence level for the posted intervals is not reported in the registry record. These omissions constrain assessment of the intended inferential framework and the robustness of the estimates.

The trial is listed as phase 2 and enrollment is 150, while the posted primary outcome analysis concerns the smaller clinically evaluable groups. The registry lists a multicenter design but does not report the number or characteristics of centers. It also does not provide detailed descriptions of outcome assessment procedures beyond the cure and failure criteria. Safety reporting includes affected counts, but not detailed timing, severity grading, exposure-adjusted comparisons, or death counts.

These limitations do not invalidate the recorded results; they define what can and cannot be concluded from the registry record. In particular, the data do not establish equivalence, comparative safety, or the applicability of the results to people outside the defined analysis population.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of a Fluoroquinolone to Treat Complicated Skin Infections — NCT00719810.
• Registry record last updated 2014-07-14; status last verified 2014-06.
• Results first posted 2010-02-03.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed randomized, double-blind, multicenter, parallel-group phase 2 study with enrollment of 150. It compared delafloxacin 300 mg intravenously every 12 hours, delafloxacin 450 mg intravenously every 12 hours, and tigecycline given as an initial 100 mg dose followed by 50 mg every 12 hours.

The primary endpoint was clinical response at test of cure 14-21 days after the last dose in the clinically evaluable population. Response counts were 33 of 35, 37 of 40, and 31 of 34 across the three arms. Comparative estimates were imprecise, with reported intervals spanning both directions of difference. A secondary MRSA response outcome was also listed, with fewer participants.

The record provides unadjusted comparisons and descriptive safety counts, but does not report the original sample-size justification, analysis plan, multiplicity approach, missing-data methods, or an all-randomized primary analysis. The findings are therefore best interpreted as estimates for the recorded populations, with material uncertainty and reporting limitations.